Scientists frustrated by the so-called “third reviewer” — the one always asking for additional experiments before recommending acceptance — might be forgiven for having fantasies of being able to review their own papers.

But one Korean scientist, Hyung-In Moon, managed to do just that, through what must have seemed like clever subterfuge at the time. And he got away with it for a while — until he didn’t, as witnessed by this retraction notice for “Larvicidal activity of 4-hydroxycoumarin derivatives against Aedes aegypti,” published in Pharmaceutical Biology, an Informa Healthcare title:

The peer-review process for the above article was found to have been compromised and inappropriately influenced by the corresponding author, Professor HI Moon. As a result the findings and conclusions of these articles cannot be relied upon.

The corresponding author and the publisher wish to retract these papers to preserve the integrity of material published in the journal. The publisher acknowledges that the integrity of the peer review process should have been subject to more rigorous verification to ensure the reviews provided were genuine and impartial. The publisher apologizes for any inconvenience rendered to the readers of the journal and wishes to assure the reader that measures have been taken to ensure that the peer review process is comprehensively checked to avoid a similar error occurring.

There are three more retractions in the International Journal of Food Sciences and Nutrition, with the same notice:

We wanted to know just how Moon had “compromised and inappropriately influenced” the peer-review process. What we learned, from Informa Healthcare managing editor Kimber Jest, was quite something:

He suggested preferred reviewers during the submission which were him or colleagues under bogus identities and accounts. In some cases the names of real people were provided (so if Googling them, you would see that they did exist) but he created email accounts for them which he or associates had access to and which were then used to provide peer review comments. In other cases he just made up names and email addresses. The review comments submitted by these reviewers were almost always favourable but still provided suggestions for paper improvement.

Moon had apparently read the same playbook as Guang-Zhi He, an author at Guiyang College of Traditional Chinese Medicine in China who made up email addresses for possible reviewers of a paper that was eventually retracted. Like He, it turns out Moon tried to be too clever. Real reviewers might have always been”almost always favourable but still provided suggestions for paper improvement.” But they wouldn’t have been so fast. Jest continued:

This came to our attention when the Editor of Enzyme Inhibition and Medicinal Chemistry, Claudiu Supuran noticed that almost all of the peer review comments were coming back in less than 24 hours. He contacted Prof. Moon who admitted to pretending to be some of the peer reviewers that he had ‘recommended’ or to asking colleagues to provide the reviews. We then provided a list of all the papers that Prof. Moon authored and published in our journals and asked him which ones were affected and if he would retract any of them based on his manipulation of the peer review process.

There will be more retractions from Informa, from Enzyme Inhibition and Medicinal Chemistry and Immunopharmacology and Immunotoxicology. The case has been frustrating to deal with, Jest tells us:

We have tried numerous times to contact his institution but have received no response. We attempted to contact all co-authors to let them know about the situation- very few replied, and most of those who did said they were not aware of Prof. Moon’s practices. Prof. Moon claimed throughout to have acted alone and that his co-authors were not involved in this activity. He was the submitting and corresponding author on all of the papers.

Informa, Jest said, will take steps to make sure this doesn’t happen again:

We have audited the peer review process for all our journals and updated our Best Practice peer review guidelines for our Editors and Associate Editors. This includes reinforcing the idea that we must have at least 1 review performed by someone that was not listed as a preferred reviewer, checking thoroughly the expertise and institution of suggested reviewers, and being suspicious of minimalistic and positive reviews coming back extremely quickly. We have recommended that editors try and use institutional email addresses as far as possible to contact reviewers and generally we raised awareness among our editors of this novel type of misconduct. We have also placed this case before COPE and have been following their recommendations which included issuing the retraction notices for the papers that Prof. Moon admitted to influencing the peer review of and agreed to retract, and investigating further the other papers he has authored with us to see if there is cause to retract these papers as well- one suggestion was to send them out for peer review again and this is an ongoing part of the case.

Informa has also added this warning on some of their journals’ article submission pages:

Please note: it is inappropriate to list as preferred reviewers researchers from the same institute as any of the authors, collaborators and co-authors from the past five years, as well as anyone whose relationship with one of the authors may present a conflict of interest. The journal will not tolerate this practice and reserves the right to reject submissions on this basis.

For his part, Moon acknowledged suggesting his friends and colleagues as reviewers, telling Retraction Watch that the results “can be mistaken for fake reviews.” But he said it wasn’t only his mistake: The editors, Moon said, invited those reviews without confirming the identity of the reviewers.

Moon denied encouraging his friends to review the papers, but admitted that that “the lack of [a] genuine and impartial review process” meant that readers can’t rely on the findings and conclusions of the articles. As a result, he proposed a retraction and agreed to the notice.

Moon also — um, helpfully? — had some suggestions on how to make sure this didn’t happen again:

There is nothing wrong with soliciting reviewers from authors, as long as there are some checks. Of course, authors will ask for their friends, but Editors are supposed to check they are not from the same institution or coauthors on previous papers. I know so many journals ask for *potential* reviewers, which they then add to a database of reviewers for the field the submission was made in. They then send the paper for review to other people on that database.

Examining the feasibility of potential reviewers is an important part of being an editor, Moon said.

Then…authors and editors will be able to avoid the problems [that occur] from the selection of reviewers.

Moon — now in the department of Medicinal Biotechnology at the College of Nature Resources and Life Science of Dong-A University, in Busan, Korea — has experience retracting papers. We found seven from several years ago:

Reason: The first author, Hyung-In Moon, has written to the journal editor indicating his responsibility for having committed major mistakes whilst conducting the experiments, and apologises to the co-authors and the readers for this retraction.

Readers may wish to know that three other papers in which Hyung-In Moon is a co-author, have also been retracted for the same reason:

This paper by Hyungin Moon and Jae-Chul Jung (DOI: 10.1002/ptr.1941)has been retracted by agreement between the authors and John Wiley & Sons, Ltd. The retraction was requested by Hyungin Moon due to errors being made in the performance of the experimental work.

This work has been supported by the KOSEF Brain Neurobiology Grant (2006), the Ewha Global Challenge grant (BK21) and Cooperative Agreement Number 1-U01 C1000211 from the U.S. Centers for Disease Control and Prevention (M.A.A.).

This Errata note will be linked henceforth to the original paper. The corresponding author and other coauthors wish to apologize to Dr Avery, the University of Mississippi and the C.D.C. for the omission of their contributions to this research, and to the readership of Molecules for any inconvenience caused.

We asked Mitchell Avery, of Ole Miss, whose name was the one added to the paper, what happened. Corresponding author J.C. Jung, Avery said, was one of his postdocs for a number of years. At some point, Moon visited the lab, then he and Jung returned to their home country of Korea and published some of the work they’d performed in Avery’s lab — without telling Avery.

I was forced to involve the University here to deal with Jung to submit errata which then included myself as author, and the agency that funded the work here (the CDC). Altogether a most unsavory situation. While Hyung-In Moon was here, he was more a colleague of Jung’s than my postdoc, and I had no hand in training him. The whole thing was very odd.

I think it is perfectly reasonable for the editor to ask the submitter about his or her preferred reviewers. Providing, of course, that these people are then excluded from the pool of potential reviewers.

Sometimes preferred reviewers can be quite critical. It’s up to the editor to be careful, and be aware of any possible biases: at least with a preferred reviewer you’re fore-warned that they might be biased.

Asking for preferred reviweers is not an uncommon part of the scientific peer review process. Many journals solicit this information, and to provide several names does not imply that the authors are seeking bias or impartiality. To the contrary, I personally have requested reviwers who I knew would be very tough on my work, knowing that if it passed their scrutiny, it would be that much stronger. Oftentimes a particular research area is very new or has only a few experts who would be well-qualified to evaluate new findings. In such cases, the editors of a journal want to know who these people are so that the work can be properly evaluated. As Bob O’Hara said in his comment, it is up to the editor to be careful. I would add that although there will always be a few clowns out there like Moon who try to subvert the scientific process (for example check WikiPedia for the scandal by Jan Hendrik Schön), on the whole it is a very robust process. The biggest shame is that people who are not engaged in science, and therefore might not know this, lose confidence in the whole enterprise when these uncommon individuals come to light.

Some high energy particle research can have hundreds of names on the final publication. There’s a great example here: http://arxiv.org/pdf/1003.3124v2.pdf. Scroll down for the list of authors (page 24 and onwards – 17 pages onward!). That’s quite a few on the blacklist!

There are also fields where collaboration is the norm on some complex and unique data. This rapidly results in highly complex author networks

In my opinion it would be wrong to think that co-authors cannot be critical of other work of the principal author(s). Sometimes they even know typical mistakes made by the groups they collaborate with, allowing a more critical review. But you can find unethical people everywhere, so there surely will be some that provide a highly biased review for ‘political’ reasons. But so will some people who you do not collaborate with, and in the other direction (maybe even _because_ you don’t collaborate with them…).

The minimum requirement for such club is 3 persons: “A”, “B” and “C”.
They are very close friends, long-time colleagues, and of course co-authors in many publications. Please, note that in order to be successful in deceiving the readers/editors/publishers about their “independence”, they should be in different institutions, preferably in different countries.

This is how it works:
Persons “A” and “B” are reviewers for person “C”.
Persons “A” and “C” are reviewers for person “B”.
Persons “C” and “B” are reviewers for person “A”.
Then, this repeats over and over again and of course each one calls the other two “top experts in the field”.

Each one is published many times based on these “INDEPENDENT” reviews.
Then, these publications are used mainly (if not solely) to deceive the authorities for gaining more public grants.

This is per se CONSPIRACY to obtain public money by deception, which is criminal offence in most jurisdictions.

In reply to Marco August 24, 2012 at 9:55
Thanks for that example and your suggestion of not in the last 5 years. The fact that you find unethical people everywhere is taken, but does not take away from the fact that it might be better to have reviewers who are not connected to you. Aiming for better, not perfection.

When it comes to those big physics publications, they still try to have at least two teams, perhaps three, working on the most important things. I think that’s how they caught Ninov. Other groups (one or two) in the world could not repeat the work.

David, why might it be better to have someone who is not connected? It’s a serious question, and one that requires a good description of “not connected”.

I don’t think the Ninov example shows anything other than it being a good idea that others replicate the results. There’s a good chance his paper was reviewed by people that were “not connected”, but did trust that the data reported was also the data obtained. A former co-author may have been more critical because he may have known the issues involved in obtaining and analyzing the data.

The quote just states not to name past co-authors as preferred reviewers at the time of submission. If the assigned editor decides to have the manuscript reviewed by a past co-author then it shouldn’t be a problem, yes?

Yes, I do understand that idea. That’s not the same as “connected”. I have quite a few examples from my own experience where people would be able to claim I was connected (as prior co-author, being in frequent contact, etc. etc.), and yet I know I would not be conflicted if I were to review their papers.

Recent example: I was “the third reviewer” on a paper by a former co-author whom I had just invited for a seminar at my department. I don’t think he knows my identity, but the response to the review comments showed a clear appreciation for my critical comments, because they helped improve the paper, whereas the comments of reviewers 1 and 2 where at best superficial, and at worse unhelpful. I would not be surprised if those two reviewers were not nearly as “connected” as I was to the senior author. Perhaps my willingness to help improve a paper by critical comments could be considered a result of my supposed “conflict”…

Yup, totally agree. It’s useful occasionally to have the point of view from one of the majority of scientists who in my experience have the basic standards of integrity to be able to make objective review of others’ work even if there is a degree of “conflictedness” because they happen to share fields or may be acquaintances or have worked together in the past. Your experience is similar to mine.

It’s maybe not a highly represented point of view on this site (which necessarily wallows in the nefarious practices of the tiny proportion of “scientists” who cheat!) that the reviewing process is largely one whereby scientific manuscripts go through a round of improvement prior to publication … even if the process can be maddening when it’s one’s own precious papers under review.

That’s not a reason that “reviewers need to be independent” David. One rather extraordinary case from 15 years ago doesn’t define the framework for assessing reviewing practices. In fact I find yours and Marco’s points of views interesting in their diametric opposition. Marco’s posts support the point of view (that I share) that scientific MS reviewing works by and large because the majority of scientists are actually interested fundamentally in finding stuff out, and have high standards when it comes to submitting, reviewing and editing scientific manuscripts. One needs rather serious failures in these elements for substandard papers to find their way into press (as this site shows these failures happen occasionally).

Incidentally, I do think that these practices are creaking somewhat, but that’s largely due to the vast proliferation of new journals full of stuff that no-one seems very interested in reading, but whose submissions have to be reviewed; although I’m broadly-speaking a biologist who has published in the pharmacological literature, “Pharmaceutical Biology” impact factor 0.878, is yet another journal I’ve never heard of before it turns up on this site.

The Beneviste case might indicate that one needs to be aware that occasionally Nature and Science (arsenic in DNA!) will be rather provocative in their publishing practices, but I don’t consider it a particularly relevant example of the run of the mill processes of scientific publishing.

David, can you explain how the publication of Benveniste’s paper shows reviewers should be independent? I don’t think Nature selected any reviewers that were “connected” in any way to Benveniste and his team. There is at least no evidence for that.

Reviewers on the first polywater papers are also unlikely to have been “connected” to the Russian group; several groups around the world even managed to reproduce the results. Ouch…artifact.

It’s not the paper. It is more fundamental.
When they tried to repeat the experiments “blind”, researchers from Benvensite’s group could repeat the experiments, researchers from other groups could not.

Why do you think we aim at an independent judiciary?
Why do you bother to use “controls” in your experiments.
I give up!

David, what I (and I think Chris) are trying to make clear that being a co-author on somebody’s paper does NOT automatically result in automatic future conflicts in reviewing papers from the person/group you have co-authored with. At best the Benveniste case makes it clear that it would be stupid to use co-authors on that paper as judges of that paper.

I also don’t understand what the independent judiciary has to do with scientists possibly reviewing papers of their former co-authors. It is not uncommon that judges, who often are former lawyers, preside in cases where their former colleagues are council for the defense.

David Hardman:
> When they tried to repeat the experiments “blind”, researchers from Benvensite’s group
> could repeat the experiments, researchers from other groups could not.

Repeating experiments is, indeed important, but should not happen at the review stage.
How could you ever publish a paper in a timely fashion if all of the reviewers had to
repeat a (possibly years long) experiment?

Still find it difficult to get your point David. You seem to be insisting that since in 1988 Nature rather provocatively allowed a dumb homeopathy paper to be published, then Marco and the vast majority of scientists (myself included) cannot be trusted to make objective reviews of scientific manuscripts under conditions where one might consider a mild degree of “conflictedness” may exist (i.e. we work in the same field as, or are acquaintances of, or worked together some time in the past with, the author(s)).

That seems a huge extrapolation to me. The fact is that the reviewing process is underpinned by elements of good faith in which scientists give up free time to make unremunerated assessment of other scientist’s manuscripts. The process is normally done within journal- or publisher-specific guidelines, and is overseen by editors that should make an effort that fair play is maintained. In my experience scientists play those roles in a rather adult manner.

Some don’t though. A small number of individuals cheat; they make up data, or doctor images, or steal other’s words or give fake email addresses so they can review their own papers! It’s difficult to escape the conclusion that Nature and Science very occasionally display rather childish approaches to selecting papers for their journals.

But we shouldn’t trash good practice by projecting onto it the sins of the cheats. Of course if one spends all one’s time on RetractionWatch then the entire scientific publishing enterprise might seem to be an edifice of chicanery; however there is a real world out there!

What should I do if I am the coauthor of a paper accepted in record time in a high profile magazine by an editor who is a personal friend of the corresponding author? He apparently has provided a list of potential reviewers, however even that could have been waived by a friend editor… I do not 100% believe in the contents of the paper, and I am just happy I am not the first author…

I was important part of the investigation for years, but in the end (after reading the final version) some of the finds by other authors seemed fishy to me and they are not willing to openly discuss their raw data with me. That is, I am not sure there is something fundamentally wrong with it, however I strongly suspect and cannot know because others are not willing to cooperate. And I do not agree with everything written, but that should be normal, and this is why I am happy for not being 1st author (=the guy who should stand by any absurdity said). Some phrases are quite far-fetched guesses.

Hibby it’s difficult to make constructive comment without knowing the details of your situation. Personally, I don’t think it is normal that you don’t agree with everything in the paper – if I sign off on a paper as a coauthor I would expect to be comfortable with everything presented and the interpretations. Of course in a multiauthor study where part of the work constitutes a set of methodologies that you’re not directly familiar with then it’s quite likely that you have to take those elements of the data and its interpretations at face value. In that case it’s important to have confidence in the trustworthiness of those coauthors. It seems like you don’t have that which is worrying.

It also depends on the stage of your career. I’ve learned over the years that you should only collaborate with individuals that share similar points of view when it comes to basic scientific integrity. In fact once I became an independent researcher those sorts of collaborations tended to happen quite naturally. However if you are at an early stage of your scientific career then you might find yourself in situations where you end up working with people that don’t share similar ethical values as you. That happened to me at one point, and if the same applies to you, then you may want to consider your present situation as a learning experience and move on. So long as you are confident in your elements of the work, and that these are properly represented in the paper, that may be sufficient grounds for sitting back and letting the situation progress to its ultimate conclusions. However without knowing the details it’s not obvious that that “hope for the best” strategy is the best one.

It’s always a good idea to talk about these situations with friends, colleagues and any other scientist you consider to be sympathetic. If you haven’t already seen this, you might find the “role-playing” videos of the US Office of Research Integrity to be interesting if not helpful:

What are you worried about? That the paper is truly flawed or that you will get caught? Or that you won’t get caught and the defective paper will mislead readers?

It can be difficult to get multiple authors to agree on the exact wording and the precise strength of conclusions. Are you 98 percent confident in the paper? Or only 50 percent confident? If somebody calls you up to discuss the paper, can you talk about what was done and what it means? Or are you going to launch into a list of the things that are not right about it? And what are those things? Overenthusiastic statement of the conclusions? Or basic defects in the research design?

Since you are glad that you are not the first author, you must be worried that something bad will happen to the first author. Will you and the other co-authors cut and run at the first doubting comment submitted by a reader? Will you claim that you were hoodwinked by the first author? Will you claim that your name was added without your knowledge?

If you think the paper is fundamentally correct, perhaps you could suggest to your co-authors that everybody would benefit from a more intensive review than you suspect the paper has received, for the sake of improving the manuscript before publication, and the corresponding author could request that the “friend” editor arrange for additional reviews. Or maybe you could persuade your co-authors that wording changes are needed. Yes, it is late in the day, but if the acceptance was a favor for a friend, wording changes will have no effect on acceptance/rejection.

Do what you can to improve the manuscript even though it has already been accepted. Or if you think the entire thing is wrong, ask to have your name removed. A few keystrokes can relieve you of anxiety.

I believe in 65% of the paper, especially on things I have seen and done. However I prevented coauthors from manipulating results whenever I could (yes, they tried and tried hard). This already deteriorated our relationship. Now there are a few details which seem fishy to me and they will not show me the raw data. And I did not foresee they would get a friend to accept the paper. This only increased my suspicions that they do not want anyone prying into the paper. I would go for your suggestion “f you think the paper is fundamentally correct, perhaps you could suggest to your co-authors that everybody would benefit from a more intensive review than you suspect the paper has received, for the sake of improving the manuscript before publication, and the corresponding author could request that the “friend” editor arrange for additional reviews.” — however they would get seriously pissed off and start persecuting me. I am not in a good political position to face the senior authors… I think the best I can do is to stand by own concluions in the paper. If asked I would say (and it is true) that some of the conclusions seemed a bit far-fetched to me but I cannot properly judge as they belong to an area I am not experienced with and I did not take part in that part of the investigation. In future investigations of my own in this area I may not confirm some observations in this paper, and therein (in my own trustful conclusions) suggest that somethings might have been overlooked/misinterpreted/whatever, and correct those.

Hibby, you might want to check ICMJE’s recommendations on authorship, in particular point 3: http://www.icmje.org/ethical_1author.html
I believe you should be happy with the whole content if you want to be listed as an author.
In your case most authors would be worried that their reputation might be in jeopardy if things go pear shaped with their paper, even if they are not the first author.

Dear Joris,
Thanks for the link, really interesting. However I must note that most colleagues I contacted for opinion declared that usually they are unhappy or at least uncertain with one or another aspect of most papers they produce with collaborator from other groups. And funny enough, especially when they hit high-impact factor periodicals (possibly because they had to conform to expected standards?).
Based on your suggested guidelines, I think I fit exaclty in “Each author should have participated sufficiently in the work to take public responsibility for appropriate portions of the content”, meaning, I have worked a lot on the paper that could not have been conceived without my participation and I stand by the veracity of all experiments I have done. This should not automatically imply that I agree with everything other authors wrote on paper, and certainly it would be impossible for me to attest that no other author manipulated other results in some manner. Well I could never be certain, especially when I have stopped them from clearly trying to manipulate some results I had directly generated.

I might be very naive, but could someone, please, explain to me the following:

WHY, “the peer-review process for the above article was found to have been compromised and inappropriately influenced” when the author was one of the reviewers for his own paper, but
the peer-review process is NOT found to have been compromised and inappropriately influenced when the editor is publishing in her/his own journal without independent review (as many as 172 times, as noted on another post on RW)?

It looks to me that the only difference between the two cases is in the number of offences, and the only conclusion I can make is that MULTIPLE misconduct is NOT considered misconduct.
So, should Professor HI Moon had done it just few more times, it most probably would be OK.

The above mentioned is a joke about the DUPLICITY in treating publication misconduct, or is it the reality?

on the lighter side….see today’s news: http://www.bbc.com/news/technology-19377261 “Apple awarded $1bn in damages from Samsung in US court” – I am just quoting the reports….what is it called? copy and paste or duplication or plagiarism?

Just like “Rape is rape”
PLAGIARISM IS PLAGIARISM full stop, no “if”s, no “but”s.

In reply to Ressci Integrity, August 25, 2012 at 10:39 pm
Ressci, why with your comments you try to divert, dilute, and ultimately make pointless all cases of serious misconduct?
It is clear for everybody that you are the Fifth column in RW, see http://en.wikipedia.org/wiki/5th_column

In reply to Hibby, August 26, 2012 at 8:14 am

Hibby, we simply should NOT stop demanding from the publisher/editor/institution to DO THE RIGHT THING.
As I have already mentioned several times on RW, when someone informs the publisher/editor/institution about irregularities with an article, they deploy the following:
1. IGNORANCE. Should the person persists, then they try
2. DENIAL. Should the person persists, pointing out irrefutable EVIDENCE, then they use
3. ARROGANCE. (i.e. So, what? That’s none of your business). Should the person persists, pointing out breaches of COPE Guidelines, institution’s Frameworks, etc., they deploy
4. INTIMIDATION.

However, unlike other offences which are easier to cover up as these are one-off events (like, for example, crossing intersection on red light, with high speed, and being intoxicated), publication irregularities are PERMAMENT !!! and these are in front of everybody! Tomorrow somebody else will point out the same irregularities.

Ultimately, by refusing to do the right thing, the publisher/editor/institution ERRODE their own credibility.
See here http://www.spsp.org/?ResponsibleConduct
Finally they got it – that “someone might not trust the integrity of one’s science”.
Now they should realize that:
Instead of ignoring/denying/cover_up committed misconduct, getting rid of the rotten apple is in everybody’s favour.

Hibby, I am in similar situation like you, where for more than 18 months I’m pointing out irrefutable evidence for multiple breaches of COPE Guidelines, publisher’s Policy and institution’s Framework, and the publisher/editor/institution stubbornly refuse to do the right thing.

Even the fraud blogs like Science-Fraud.org seems to ignore fraud evidence from Brazil. I do not know where you are, but apparently, when it comes to the 3rd world, there is additional advantage to fraudsters: no one cares AT ALL… Anyway thanks for the reassuring words.

Regarding co-authors being reviewers, NIH has a fairly simple policy on this – you’re officially “in conflict” with a grant proposal (and have to leave the room while it’s being reviewed) if you co-authored a paper in the last 3 years with any of the applicant team. It’s a policy that is congniscent of the fact that sometimes the best expert on someone’s work is a person who has actually worked with that researcher in the past. 3 years seems like a reasonable statute of limitations IMHO.

NIH also finds you in conflict if you work for the same University, even if you have no prior interactions or publishing history or are even in the same field. Compared with this, vehdwig’s “reasonable statute of limitations” is ludicrous. I am *much* better acquainted with some guy that I drink beers with at a conference, shoot the breeze about our latest data and bemoan the disrespect for our sub-sub-field at HighImpactJournal and in the study sections….even though we’ve never published together. and may appear to naive eyes to be competitors.

1. Most of research proposals contain apriori known lies and exaggerations. Some of the most important discoveries though were made using grant money given for completely different purposes (which in many other fields would be considered a crime).
2. Peer reviewed process was implemented dozens of times in history, always resulting in predominance of run-of-the-mill incrementative research over anything unusual or challenging.
3. In the recent history of Science, I don’t remember a single Professor ever convicted for either:
a. Misleading his graduate students.
b. Misleading grant agencies about validity or reproducibility of his research.
c. Forming a partnership with other professors with the purpose of mutual promotion in “independent” reviews, including grant applications, irregardless of their actual merit.
d. Willfully and knowingly suppressing conflicting evidence.
It’s not Wall Street, where attaining financial gain through aggressive interpretation of quarterly results or providing unrealistic guidance to investors is a very easily path to jail. Scientific progress is a complex phenomenon and denies the possibility of immediate objective evaluation.
4. As one of a few leading inventors in my field, the only use I ever find for reviewer’s comments – is whether the paper is written well enough for an average person to be able to understand it. It is a valuable service, but I doubt it is what reviewing process is supposed to accomplish. I am certain 80% of reviewers did not even read my articles from a to z.

“We asked Mitchell Avery, … what happened. … At some point, Moon visited the lab, then he and Jung returned to their home country of Korea and published some of the work they’d performed in Avery’s lab — without telling Avery.”

“While Hyung-In Moon was here, he was more a colleague of Jung’s than my postdoc, and I had no hand in training him. The whole thing was very odd.”

I imagine that these circumstances must have been rather trying for Prof. Avery. Nevertheless, it would be interesting to know, based on this description, what aspect of his role satisfied the requirements of the COPE guidelines on authorship. I’m sure there must be more to the story, but on a first reading of the above, he appears to have explicitly disavowed any role in conception of the work, its undertaking, or the writing of the paper.